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DEC 29 ODf DEPARTMENT OF THE AIR FORCE D

AIR UNIVERSITY (ATC)

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Dist Special L VL

AN INVESTIGATION OF EXPERIMENTDESIGNS FOR APPLICATIONS

IN BIOFEEDBACK-PERFORMANCERESEARCH METHODOLOGIES

Gilbert Fried, Captain, USAF

LSSR 83-80

DTICELECTE

DEC 29 9800

D

DISTRIBUTION STATEM A

Approved for public zeleaseQDistribution Unlimited

The contents of the document are technically accurate, andno sensitive items, detrimental ideas, or deleteriousinformation are contained therein. Furthermore, the viewsexpressed in the document are those of the author(s) and donot necessarily reflect the views of the School of Systemsand Logistics, the Air University, the Air Training Command,the United States Air Force, or the Department of Defense.

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3. The benefits of AFIT research can often be expressed by the equivalentvalue that your agency received by virtue of AMI performing the research.Can you estimate what this research would have cost if it had beenaccomplished under contract or if it had been done in-house in terms of man-power an/or dollars?

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4. Often it is Uot possible to attach equivalent dollar values to research,although the results of the research may, in fact, be important. Whether ornot you were able to establish an equivalent value for this research (3 above),what is your estimate of its significance?

a. Highly b. Significant c. Slightly d. Of NoSignificant Significant Significance

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19. K EY WORDS (Caunhae on reverse side It a,...aomy ld 16dmwet1 by bAoeh ftaww)

Biofeedback Human PerformnanceElectromyogram. Relaxation TrainingExperimental Validity Self-RegulationExperiment Design

20. ABSTRACT (Coeothum ov, reverse aide i1 eeeaw ad Idmiill by Weekb mbxwe)

Thesis Chairman: Saul Younq, Lt Col. USAF

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'or a number of years biofeedback techniques, to ccn:rol physio-logical responses, have been gaining wide acceptance in the area ofclinical research. A previous thesis experiment expiored thepossibility of using these techniques to enhance task performance;however, no significant results were obtained. The purpose of thisthesis was to research the literature on experiment design tech-niques to gain a better understanding of experiment designcomplexity and, in so doing, find other avenues of approach whichmay lead to more significant results. The material coveredincluded (If five general experiment designs which are consideredto be the basic 'building block" techniques for numerous otherhybrid dcsigns; (-l experiment design with humans concentrating ont"'e important concepts of internal and external validity; andOf biofeedback experimental research efforts with an eye towardtask performance and any relationships to the previous thesiseffort. As a result of the investigation several shortcomings ofthe original experiment were pointed out and two recommendationswere advanced for increasing the validity of any future attempts atbiofeedback/taak performance research.

4 UNCLASSI FIrDSIRCURITY CIrASPICATIOll OF 71-1- PAG( Lh al Do qes E)

_ _ . . . . . .- . . . . .. ,._:_ . -L i5 . . ..?

II

LSSR 83-80

AN INVESTIGATION OF EXPERIMENT DESIGNS FOR

APPLICATIONS IN BIOFEEDBACK-PERFORMANCE

RESEARCH METHODOLOGIES

A Thesis

Presented to the Faculty of the School of Systems and Logistics

of the Air Force Institute of Technology

Air University

In Partial Fulfillment of the Requirements for the

Degree of Master of Science in Systems Management

By

Gilbert Fried, BSCaptain, USAF

September 1980

Approved for public release;distribution unlimited

- - - -

This thesis, written by

Captain Gilbert Fried

has been accepted by the undersigned on behalf of thefaculty of the School of Systems and Logistics in partialfulfillment of the requirements for the degree of

MASTER OF SCIENCE IN SYSTEMS MANAGEMENT

DATE: 19 September 1980

COMTTEE AIRMAI

RDREADER

ii

ACKNOWLEDGEMENTS

I wish to express my sincere appreciation and thanks,

first and foremost, to my wife Helene for accomplishing not

only the typing of this thesis but also being able to "keep

the home fires burning" through these long days and nights.

Also, a special thanks goes to my twin sons, Mike and Doug,

who endured many hours of uncharacteristic quiet while I

pursued the completion of this effort.

I also thank my thesis advisor, Lieutenant Colonel

Saul Young, for his guidance, strong encouragement, and

friendship through this effort; and my reader, Lieutenant

Colonel Edward J. Dunne, for his valuable insight and

suggestions which aided in the successful completion of the

thesis.

Finally, last but not least, a note of thanks goes

to the School of Systems and Logistics librarian, Jim Helling

and his staff, for their kind and courteous assistance in

gathering research material.

iii

TABLE OF CONTENTS

Page

ACKNOWLEDGEMENTS..................... . . .. .. .. . . ...

LIST OF TABLES.......................vi

CHAPTER

I. INTRODUCTION....................1

Background....................1

Statement of the Problem.............6

Objectives....................7

Scope and Limitations..............8

Methodology....................8

II. GENERAL EXPERIMENT DESIGN.............10

Background....................10

Terminology and Definitions...........12

Experiment Design Methodologies.........23

III. EXPERIMENT DESIGN WITH HUMANS...........39

Background....................39

Experimental Validity..............41

Human Subject Experiment Designs.........51

IV. BIOFEEDBACK EXPERIMENTATION ANDTASK PERFORMANCE..................62

Background.....................62

GnBiofeedback n Eorne...............69

Gieea k Bifedbc Pexerimnentai..........64

iv

PageI V. SUMMARY, CONCLUSIONS. ANDRECOMMENDATIONS .................. 79

Summary......................79IConclusions. ....................82Recommendations .. ................ 84I SELECTED BIBLIOGRAPHY....................86

A. REFERENCES CITED...................87

B. RELATED SOURCES....................90

BIOGRAPHICAL SKETCH OF THE AUTHOR..............91

vi

LIST OF TABLES

Table Page

1. Completely Randomized Design Layout . ....... . 26

2. Randomized Block Design Layout ... .......... . 29

3. Latin Square Design Layout (3X3) .. ......... . 32

4. Possibilities for Latin Squares .. ......... . 33

5. Incomplete Block Design Layout (Balanced) . ... 35

6. Experiment Design Layouts .... ............ 54

vi

Chapter I

INTRODUCTION

The striving for increased performance is everpresent

on the minds of top management whether it be in business and

industry or in the United States Air Force. In the Air Force,

mission performance is a primary goal and a significant por-

tion of that goal may be reached by concentrating on improving

human task performance. The human factors discipline has

made great strides toward that end in the area of individual

and machine interaction. But can individual performance also

be improved by learning to control one's own physiological

responses to task oriented situations?

Backaround

Eastern civilizations have, for many years, known

techniques for voluntary control of physiological body functions;

however, it was not until the social revolution of the 160s

that any serious effort at scientific study was undertaken.

As Hume wrote, in a 1976 review of biofeedback research (23:1),

"Ten years ago anyone writing a review of research in this

area would have had difficulty in filling a postcard with the

relevant information." Along with the public's involvement in

mind and consciousness raising, the scientific community's

interest in the relatively young discipline of psychophysiology

1

-_-_-------------

emerged. This discipline is concerned with the complex

relationship of mind and body. Psychologists held pro and

con opinions concerning the possibility of modifying auto-

nomic nervous system activity through operant conditioning

methods (basically a reward system for behavior that induces

a satisfactory response). To provide insights into the

mechanism and scope of these mind-body interactions biofeed-

back research techniques were developed (8:v; 9:2).

Biofeedback is basically a process of "feeding back"

information about an individual's physiology to the individual

generating that information. The psychophysical technique

involves monitoring physiologic activity about body functions

such as heart rate, blood pressure, skin temperature, muscle

tension, or brain waves. The information is "fed back" by

visual and/or auditory means indicating changes in the activity.

An individual then must develop a personal mental mechanism

whereby voluntary control over the physiologic activity is

exerted (9:3-4).

When biofeedback burst on the scene it was picked up

and touted by the popular press as a natural panacea therapy

for the cure of many forms of illness. This was done many

times without adequately assessing the true value of the

experimentation that was accomplished. One of the biggest

problems in this area, partly due to the nature of the process

is substantiating the claimed cures used in advertisements by

biofeedback therapists, training schools, and equipment

2

suppliers. Fortunately, a significant amount of work has

been done by competent researchers over the past 15 years.

In 1969 the the Biofeedback Research Society was founded by

a group of psychotechnologists interested in furthering

research and applications in the field of self-regulation.

With the group expanding, in 1976 the name was changed to the

Biofeedback Society of America and now has 1100 members with

eight state groups. The society publishes a quarterly journal,

a quarterly newsletter, and proceedings of its annual meetings

(10; 23:1; 39:v).

In a relatively short time period, with calmer heads

prevailing, biofeedback has been recognized as having many

worthwhile applications but also many limitations. No less

an august body than the National Aeronautics and Space

Administration (NASA) is presently investigating the use of

biofeedback techniques for its space shuttle program. Astro-

nauts are learning to control physiological attributes such

as heart rate and blood pressure in an effort to reduce the

effects of motion sickness (4:54).

As in the NASA investigation mentioned above, a look

at several current publications (8; 9; 23; 34; 39) dealing

with biofeedback indicates that a vast majority of the material

deals with clinical research and applications. Areas of

concern include hypertension, migraine headaches, tension

headaches, heart rate disorders, and insomnia just to name a

few. The investigation of biofeedback techniques as a task

3

performance enhancer has been relatively unexplored. The

possibility of performance benefits gained from active use of

biofeedback piqued the interest of Professor Young at the Air

Force Institute of Technology (AFIT). This interest stemmed

from the fact that Young had been involved with clinical

applications of biofeedback for some time. That involvement

resulted in a 1979 AFIT thesis by Kipperman (26) which attempted

to show a relationship between the use of biofeedback tech-

niques and performance.

The Experiment

Under an original concept of Young's, Kipperman's

biofeedback research was concerned with studying the possibility

of improving pilot performance. The experiment employed a

single physical task of pitch tracking, with no induced motion,

using a pilot control stick and a vertical motion display.

The experimental environment was an enclosed Roll Axis Tracking

Simulator supplied by the Aerospace Medical Research Laboratory

at WPAFB. The biofeedback technique used was the electro-

myogram (EMG) which measures the amount of muscle electrical

activity. This indication has been found to be an accurate

representation of muscle tension level.

Biofeedback training and EMG feedback was conducted

using electrodes placed on the subject's foreheads to measure

the electrical activity of the frontalis muscles. The training

consisted of one 30-45 minute session where relaxation and

physiological control techniques were explained and practiced.

4

This was followed by a 5-10 minute reinforcement period before

each tracking session which consisted of eight runs. Question-

naires were filled out to identify any differences in demo-

graphic variables that could affect the experimental outcome.

The twenty male volunteers who participated were then assigned

to three experimental groups. Seven received EMG feedback

training and active EMG feedback during tracking, six received

only EMG feedback training, and five received no training or

active EMG feedback. The remaining two were considered expert

trackers and after EMG feedback training received active EMG

feedback on half of their tracking runs. Each subject was

scored by computer, for tracking error, on at least 48 runs

each having a duration of three minutes. The experimental

analysis was accomplished using the data base of tracking

error scores and corresponding EMG electrical activity values

(26:2-3,5-6,16-17).

Analysis and Results

Multivariate data analysis techniques were employed

using a standard statistical computer program package. The

analyses used included linear regression, correlation, and

analysis of variance (ANOVA) methods to test for significance

of several entering variables on a particular criterion

variable. A scatter diagram program was also used to provide

visual plots of each subject's tracking error score versus

run number. The data was grouped for analysis in the following

three ways: (1) aggregated by individual, (2) aggregated by

run number, and (3) individually (26:21).

5

__ _ _ _ _ _ _ _ _ _ _J~-~-

The results of the analyses were not significant in

terms of the major hypothesis proposed. The most conclusive

result of the analyses performed was in an area not directly

related to the experiment. The scatter diagrams of tracking

error score versus run number showed that a logarithmic

relationship in a learning model is valid. No significant

differences between experimental groups were found when

tracking error score was used as a single measure of perfor-

mance. The experiment did not indicate that active EMG feed-

back or EMG feedback training was a significant predictor of

performance enhancement. In fact the analyses showed that

active biofeedback was associated with a lower rate of

learning (26:39-41). The question then is, why were the

results of the experiment generally inconclusive?

Statement of the Problem

In experimental research the design of the experiment

has a major effect on the results achieved. This is an area

of real concern and may well have been a cause for the lack

of meaningful results. It has been postulated that a counter-

active effect, of hearing a constant biofeedback signal,

prevented full concentration on the tracking task and resulted

in a degradation of performance (26:41). Another possibility

for not achieving valid test results was the integration of

the task learning experience at the same time the biofeedback

data was collected.

6

I __ _______________________________________

An experimental methodology needs to be found that

will indicate task performance improvement or degradation

without the possible negative effects mentioned above. If a

more valid experimental method can be found and utilized, the

results obtained should clearly show any significance, or

lack thereof, between subjects who have or have not received

exposure to biofeedback techniques.

Objectives

Primary Objective

The purpose for this thesis is to investigate the

available literature concerning experiment design techniques.

The intent is to gain knowledge of other possible avenues of

approach which may lead to increased validity of experimental

results from research on task performance improvement through

biofeedback techniques.

Secondary Objective

A second purpose for this study is an attempt to

synthesize some of the work accomplished in the area of

experiment design techniques.

Personal Obiective

Through exploration in the area of experiment design

I will, at a minimum, expand my awareness of the inherent

complexity of the field and many of the methodologies employed.

Armed with this knowledge, I can better evaluate the relative

success alluded to in research reports.

7

-A_ _ _ =NI

Scope and Limitations

This thesis is intended to explore existing experiment

design techniques with an orientation toward idiopathic

studies. In terms of biofeedback research, idiopathic refers

to a strategy that is peculiar to the individual in attempting

to voluntarily control some physiological activity. In light

of the primary objective, the research is limited, as much as

possible, to areas involving task learning and task perfor-

mance evaluation. The broad scope of the experiment design

discipline and the time constraint inherent in this effort is

a limiting factor in the treatment of experimert design and

associated statistical methods. Also, this author is pain-

fully aware of his limited knowledge in the area of statistics;

therefore, except for the possible mentioning of techniques

that may be applicable to particular experiment designs, any

rigorous treatment of statistics underlying the experiment

designs will be left for the statisticians to work through.

Methodoloqv

This thesis is intended to provide a literature

review of experiment design techniques with an eye toward the

possible improvement in design validity of biofeedback task

performance enhancement research. To accomplish this, first

covered is some of the general experiment design literature

to gain an overall insight in the field. Next, major emphasis

is placed on investigating existing literature concerning

specific problems in experiment design with humans. Following

SI

that is a look into some of the current literature on biofeed-

back experimentation to discover what, if any, research has

been accomplished in the area of task performance enhancement.

Finally, using the experiment design information available,

Kipperman's experiment is evaluated in terms of design

methodology and validity factors with an eye toward promoting

a more successful experiment methodology in biofeedback per-

formance enhancement research.

Chapter I of this thesis has introduced the subject

matter, provided background material, and the overall research

approach. Chapter II comprises a discussion of the experi-

ment design discipline as a whole.

9

I - - - ---- _ _

Chapter II

GENERAL EXPERIMENT DESIGN

Chapter I, comprising the introduction to this thesis,

discussed the biofeedback phenomenon and the task performance

experiment using biofeedback technology. The lack of sig-

nificance in the test results led to questions about the

validity of the experimental methodology and thus to the

primary objective of this effort. This chapter will cover

experiment design techniques using a "broad brush" approach

to gain overall knowledge of the subject. Later chapters will

delve into narrower areas consisting of experiment design

with humans and biofeedback experimentation. To introduce

this chapter let us first look at the evolution of the science

of experiment design.

Backqround

Federer and Balaam, in their discussion of the develop-

ment of experiment design (15:40), first credit the mathema-

tician L. Euler for his work in 1782 as "having a profound

effect upon research on the construction and properties of

experiment and treatment designs . . ." Also of some impor-

tance to modern experiment design was a paper written in 1832

that describes methods for statistical comparisons in dealing

with the standardization of weights and measures. During the

10

same period research began in the area of agricultural methods

which eventually led to a comprehensive theory of experiment

design. As Finney (16:45) stated, "The first great stimulus

to the development of the theory and practice of experimental

design came from agricultural research." In fact, several of

the standard terms used in experiment design today owe their

origins to the work done in agricultural research (16:46).

Modern experiments in agriculture began in France, in

1834, when Boussigault undertook the first practical field

experiments on his farm. In England, in 1841, John Bennet

Lawes was instrumental in establishing the Rothamsted

Experimental station on his farm. Joined by J. H. Gilbert in

1843, they spent almost the next six decades in carefully

planning and executing field experiments. Many others toiled

in the field of agricultural experimentation through the 19th

and into the early 20th century; however, most of the field

layout designs then in use resulted in conclusions that were

difficult to validate. It is at this point, chronologically,

that the name R. A. Fisher crops up in much of the background

literature in experiment design (15:40; 16:45).

Fisher's realization of the problems in validating

field testing results led him, from 1923 on, to study the

underlying principles of scientific experimentation and

eventually to develop new design techniques. His writings on

the subject are of tremendous importance especially the book

first published in 1935 entitled The Desian of Experiments.

No one can dispute the fact that other individuals have made

11

great advances in the science of experiment design beyond

what Fisher has accomplished; however, his work is still

recognized by many as the cornerstone in the field. The

following quotes certainly attest to that fact. Federer and

Balaam (15:40) remarked that "It might be stated that experi-

ment design as known today, had its beginning with Sir Ronald

A. Fisher," Kempthorne (24:vii) wrote that "His contributions

to the Logic of the scientific method and of experimentation

are no less outstanding, and his book The Design of Experi-

ments will be a classic of statistical Literature.," and

Finney (17:1) stated, "Fisher's book remains the classic

that everyone having any concern with experimental design

must read . . ." Thus, much of the experiment design

discussion in this chapter, while drawn from many sources,

relies heavily on the pioneering work accomplished by Fisher.

But before that can be accomplished some terminology and

definitions need to be explained so that the uninitiated may

comprehend what is to follow.

Terminology and Definitions

It may be of interest to note that while pouring over

the literature in the field no general consensus could be

found as to whether "experiment design" or "experimental

design" is the proper terminology. Federer and Balaam (15:8),

no doubt concerned, saw fit to devote a paragraph to this

problem. They, in essence, said that published literature is

highly confused in use of the term experimental design. It

12

........ .... .... .. . ...... ... .... ... ...I I I .... .I T ' | ... .I ... . . .. .... ....... ... ...

has been used in discussions of selection of sample size or

treatments and conduct or analysis of experiments. Their

opinion was that "experiment design" was a more appropriate

term since it compares more favorably with other research

terms such as treatment design and survey design. So, recog-

nizing the astuteness of their argument, this author has opted

to use "experiment design" throughout this thesis. In any

event, regardless of which term one prefers, what does it

actually mean? In a number of references (1:87; 15:1; 27:87)

experiment design is defined rather succinctly as the method

or approach whereby treatments are arranged or placed on

experimental units. Finney (16:3) defines it more broadly as,

(i) the set of treatments selected for comparison;(ii) the specification of the units (animals, fieldplots, samples of blood) to which the treatments areto be applied; (iii) the rules by which the treatmentsare to be allocated to experimental units; (iv) thespecification of the measurements or other records tobe made on each unit.

The terms mentioned above plus others basic to the science of

experiment design will now be defined. Note that since a

number of books researched on the subject describe and/or

define terminology the definitions below have been constructed

from several sources.

Alternative Hypothesis

A statement of value for a dependent variable that is

phrased to contradict the null hypothesis is called an alter-

native hypothesis. The alternative hypothesis is usually the

13

one that a researcher hopes to affirm; however, it cannot be

proven directly but is one that remains tenable if the null

hypothesis is rejected (see Null Hypothesis), If the alter-

native hypothesis is accepted then it becomes possible to

infer that the experimenter's original research hypothesis

is true (27:23; 31:16).

BlockinQ

When available experimental units are not homogeneous

in nature the inherent differences in characteristics tend to

mask treatment effects. By grouping the units by their

similarities into blocks under different treatments the

sources of heterogeneity are effectively isolated. These units

are then relatively homogeneous within each block and uncon-

trolled variations can then be measured by comparisons between

them. A major purpose of blocking is to increase the power of

an experiment to detect treatment effects which is accomplished

by variance analysis. Blocking is one of the terms carried

over from agricultural experiiaentation. In accomplishing

field plot trials of soil treatments compact blocks of adjacent

plots were used to control the effects of soil heterogeneity

(1:86; 16:50; 25:31).

ConfoundinQ

When comparison tests can only be made for treatments

in combination and not for a separate treatment in question,

then the dependent variable effects are s id to be confounded.

14

- -~- --.

Effects due to one treatment variable cannot be distinguished

from effects of other treatment variables. Confounding is

sometimes deliberate when an attempt is made to reduce the

number of treatment level combinations assigned to experi-

mental unit blocks. In many instances confounding also arises

as an inadvertent imperfection of an experiment design. This

ultimately has the effect of confusing the experimental

results (25:58-59; 27:553).

Correlation

When a researcher is concerned with the strength of

the relationship between variables, rather than the prob-

ability of observing a particular value, then the concept of

statistical correlation is useful. The quantitative expression

used to denote the extent of the relationship between two

variables is the correlation coefficient. The values of the

coefficient will vary between +1.00 and -1.00. Positively

correlated variables increase or decrease in value in the

same direction, with perfect positive correlation indicated by

a value of +1.00. Negatively correlated variables increase

or decrease inversely with respect to each other, with perfect

negative correlation indicated by a value of -1.00. A value

of zero indicates no correlation between variables. Usually,

in inference testing, the null hypothesis is stated as zero

correlation between variables. A rejection of the null

hypothesis in favor of the alternative hypothesis will then

indicate evidence for the existence of correlation (25:66;

31:18; 37:94-95).

15

Dependent Variable

A dependent variable is usually a measurable quantity

that is observable but is not controlled by the experimenter.

Rather, it is a chosen indicator that reflects the effects

associated with manipulation of an independent variable or

variables. The quantification is important so that a statistical

analysis may be accomplished to make inferences about a

research hypothesis (27:5; 31:10).

Experimental Unit

The smallest part of a sample population that is

differentiated for the purpose of receiving some treatment is

designated an experimental unit. In agricultural research a

small area of land chosen for a treatment, with dimensions

specified by an experimenter, is called a plot. The term has

stuck and is used in other experimental disciplines to denote

an ultimate experimental unit even though it may refer to

something entirely different than an area of land (16:461; 27:555).

Hypothesis

Webster's dictionary (42:410) defines hypothesis as

"a tentative assumption made in order to draw out and test

its logical or empirical consequences . . . Hypothesis implies

insufficiency of presently attainable evidence and therefore

a tentative explanation." In experiment design literature

this definition is typically treated in two distinct parts

(see Research Hypothesis and Statistical Hypothesis).

16

Independent Variable (Treatment)

A variable that is under the control of the experi-

menter so that it can be manipulated to assume different

values is termed an independent variable. The terms independent

variable and treatment are used interchangeably. A broad

definition proposed by Linton and Gallo (31:8) is that

any variable, regardless of type, that is assumed to

produce an effect on, or be related to, a behavior of interest."

In practice, different values of an independent variable

(treatment) are applied in order to confirm or deny the

existence of differential effects on a dependent variable

(25:296, 27:4-5).

Null Hypothesis

A researcher performing an experiment typically hopes

to find differences in a dependent variable of experimental

units that have either received or not received a particular

treatment. The null hypothesis is a statement of value for

that variable, phrased in such a way as to negate the

possibility of a relationship between the treatment and

dependent variable in question. The null hypothesis is the

statement under test and is assumed to be true. If it is

rejected under a test of significance then the alternative

hypothesis can be accepted (see Alternative Hypothesis). To

understand this reasoning it is important to bring up the

notion of indirect proof. Runyon and Haber (37:166) describe

it in terms of "the logic of statistical inference." The

17

....A __ _

null hypothesis, as an exact statement of value, can never be

statistically proven. Also, the alternative hypothesis, as

a mutually exclusive statement, is always proven indirectly

through the rejection of the null hypothesis under an acceptable

level of risk (see Test of Significance). As Fisher (18:16)

points out,

In relation to any experiment we may speak of thishypothesis as the "null hypothesis," and it shouldbe noted that the null hypothesis is never provedor established, but is possibly disproved, in thecourse of experimentation. Every experiment maybe said to exist only in order to give the factsa chance of disproving the null hypothesis.

In other words, the conclusions made about any experiment are

not absolute and remain open to further questioning. The one

statement that can be made without any hesitation is that

findings or hypotheses can never be asserted as true without

any doubt (27:23; 31:15-16; 37:166-168).

Population

In statistical usage the term popuation refers to any

finite or infinite collection of individuals or observations

governed by an identifiable set of rules which determine

membership. Population statistical parameters are seldom

measured in experimental research due to the restriction of

size; therefore, population parameters such as means or standard

deviations are usually estimated by sample values drawn from

the overall population and by applying appropriate statistical

methods (27:2; 31:14).

18

Randomization

The idea of complete randomization is to allow each

experimental unit an equal chance of receiving each possible

treatment. If randomization can be accomplished any biases

in the treatment effects resulting from uncontrolled error

variations may be eliminated. The tests of significance on

any dependent variable in question then can be considered

valid. An important point to consider is that a so-called

"haphazard" selection process can be fraught with unintended

biases. One sure way to avoid this problem is to use a random

number generator or table for assignment of treatments and

experimental units. Also, it is not necessary to assure

complete randomization if the variation introduced is known

to be of negligible effect and will not vitiate the results.

The relevance of this concept is evident by this statement

of Lindquist's (30:11-12) that, "one of the most important and

basic of all principles of experimental design is thus the

principle of randomization" and Montgomery's (32:3) comment

that, "Randomization is the cornerstone underlying the use of

statistical methods in experimental design." As one of the

significant contributions formulated by Fisher, randomization

is considered one of the few truly modern characteristics of

experiment design (1:86-87; 13:6-8; 16:32).

19

Replication

The meaning of replication is the collection of data

from two or more observations with the experiment being

performed under a set of identical experimental conditions.

Of course this is an ideal situation and rarely happens in

fact. Practically, a researcher will attempt to hold the

variations in experimental conditions to a minimum. The basic

experimental layout is held intact though changes in place

and time may occur as the experiment is repeated. The intent

of replication is to increase precision and gain a closer

estimate of sampling error. With increasing replications

comes an increase in experiment sensitivity and decrease in

error of treatment comparisons (24:177; 25:249; 27:3; 29:72).

Research Hypothesis

The research hypothesis is a word statement that

presumes a relationship between independent and dependent

variables. The hypothesis may be derived from a theory,

observations, or simply educated guesswork; however, as a

word statement it cannot be tested directly but must be

transformed into a mathematical value (see Statistical

Hypothesis) that can be compared (27:3; 31:15).

Sample

A sample is a subset or part of a population made

available by some process, usually deliberate selection, for

the purpose of investigating particular properties of the

20

__ _ _ _ _ _ ___ _ _ _ _ _ _I.

parent population. Random samples are drawn from populations

of interest using the methods described for randomization

(see Randomization). In practice though samples rarely ever

meet the strict criteria for randomness. But they are treated

as though they did if no systematic biases exist that could

be expected to invalidate the results (25:254; 27:2; 31:15).

Statistical Hypothesis

The assumed research hypothesis forms the basis for

the statistical hypothesis. The statistical hypothesis becomes

a mathematical statement of a proposed value for one or more

parameters of a population. Since the statistical hypothesis

must be logically derived from the research hypothesis, its

acceptance or rejection gives the researcher a basis on which

to evaluate the truth or falsity of the initial research

hypothesis. To reach this conclusion the experimenter must

actually formulate two mutually exclusive and dichotomous

statistical hypotheses (see both Null and Alternative Hypothesis)

from the research hypothesis (21:12; 27:3,23; 31:15).

Test of Significance

The use of tests of significance allows a researcher

to evaluate the probability that some observed sample value

of a dependent variable would occur, given that the stated null

hypothesis were true. Typically, a test statistic with a

known probability distribution is employed to define the

probability of that null hypothesis. One of the most powerful

21

ifI . . ... . .. .. b i .. . .i ' i . ._. . . . .A

and widely used statistical tests (pick up any book on

statistics or experiment design and it will be discussed in

detail) is the analysis of variance (ANOVA) technique. The

set of procedures developed can be used for simple as well as

complex experiments involving simultaneous comparisons of

many variables. If the probability associated with the test

statistic is sufficiently low then the null hypothesis can be

rejected and the alternative hypothesis affirmed. If the

opposite occurs then the null hypothesis cannot be rejected.

Either way, the test of significance provides the researcher

with statistical evidence for concluding that there are or

are not true differences between dependent variables under

different treatments (20:92; 27:4; 31:17,122).

It should be noted that the listing of terms was

accomplished alphabetically for convenience only and there-

fore has no intended hierarchical effect. Also, it should

be apparent that the listing is by no means exhaustive: how-

ever the terms defined here, as chosen from several sources,

are those that were deemed important to a basic understanding

of experiment design concepts. Other terms that may crop up

in this and later chapters will be discussed as necessary when

they occur. The next section includes a discussion of several

experiment design methodologies.

22

Experiment Design Methodoloaies

In researching literature for this section this author

was struck by the myriad of text books dealing with the subject

of experiment design and related statistical concepts. This

is evidenced by the bibliographical listing accumulated for

this thesis which is but a small portion of the material

available. One reason for the plethora of information seems

to be that experiment design techniques cut across a wide

diversity of physical and social sciences. Thus, researchers

in each discipline have published works relating to experi-

ment design with methodologies that are geared to studies in

a particular science. With so many design approaches available

the problem then was how to limit the scope to fit within the

framework of this discussion of general experiment design.

After some thought, the solution that emerged was to

attempt a "common thread" approach to reviewing the literature.

The reasoning was that there would be some methodologies

repeatedly covered that could then be considered as basic

experiment designs and those would be the ones discussed here.

Before getting into individual methodologies though, an

important consideration for comment is the question of what

constitutes a "good" experiment design?

Foremost to the accomplishment of a successful experi-

ment is to plan in detail just what is actually required.

This involves formulating a clear statement of the problem to

be investigated. Once that step is done then the researcher

23

can determine the other interrelated activities that make up

the complete experiment design. These include items such as

setting up a statistical hypothesis to test, planning for the

collection and analysis of data to test the hypothesis,

defining the treatments to be applied, selecting the sample

population to be investigated, and selecting the criterion

(dependent) variable to indicate variation effects of the

treatments (21:1; 27:1). As important considerations for the

activities mentioned above Lindquist (30:6) summarizes and

Kirk (27:22) essentially concurs with a number of essential

characteristics of a good experiment design as follows:

1) It will insure that the observed treatmenteffects are unbiased estimates of the true effects.

2) It will permit a quantitative description ofthe precision of the observed treatment effectsregarded as estimates of the true effects.

3) It will insure that the observed treatmenteffects will have whatever degree of precisionis required by the broader purpose of the experiment.

4) It will make possible an objective test of aspecific hypothesis concerning the true effects;that is, it will permit the computation of therelative frequency with which the observeddiscrepancy between observation and hypothesiswould be exceeded if the hypothesis were true.

5) It will be efficient: that is, it will satisfythese requirements at the "minimum" cost, broadlyconceived.

With that short excursion into what constitutes a

"good" design concluded, the original focus of this section

will now be continued. In searching through the literature

for that "common thread," five types or approaches to experi-

24

ment design were discussed most often, not necessarily as

simple basic designs, but as major constructs or building

blocks for any of the most complicated designs. Both Kirk t.(27:11) and Lindquist (30:7) make essentially similar state-

ments in that regard. The remainder of this chapter will

therefore be devoted to descriptions of the following design

methodologies; completely randomized, randomized block, Latin

square, incomplete block, and factorial. Much of the presen-

tation is based on information culled from references of

Finney (16), Hicks (21), Kirk (27), and Lindquist (30); there-

fore, specific citations to these sources will not be made

unless an important point is raised by an individual author.

Completely Randomized Design

Probably the simplest of all designs, in terms of both

formulation and statistical analysis, is one in which the

relevant treatment levels and experimental units (plots) can

be randomly chosen for interaction. In the completely

randomized design no restrictions are placed on randomization.

What that means is that not only are plots randomly selected

from the available sample population but also the treatments

under investigation are randomly assigned to the plot groups.

A typical layout for this design is shown in Table 1 and the

symbolism used is defined as follows:

25

V

T. = Treatment variable or levelI

X. = Random Treatment interacted with random plot

X. = Mean of summed data under treatment T.

TABLE 1

COMPLETELY RANDOMIZED DESIGN LAYOUT

T1 T2 T.

Xl XI Xl11 12 lj

X2 1 X22 X 2j

Xil xi2 . xij

1 2 "

The analysis is made by summing the plot data under each treat-

ment variable and then performing hypothesis testing by com-

paring the means. The analysis usually consists of a one-way

(single treatment variable) ANOVA with the null hypothesis

stated as no difference between level effect means.

This design has several advantages. First, it is

flexible in that any number of treatments and/or plots can be

used. The number of plots can be varied from treatment to

treatment, however the recommended procedure is to equally

divide plots among the treatments; second, the analysis used

is relatively easy even if the numbers of plots for all

26

treatments is not the same, or the uncontrolled sources of

variation (experimental error) in the data differ from treat-

ment to treatment; third, the method of analysis remains

unchanged even when results from plots are missing and the

relative loss of information due to unavailable data is less

than with other more complex designs. The experimental error

mentioned above leads to an important area of consideration

for researchers and also to the principle criticism of the

completely randomized design.

Experimenters always attempt to minimize error effects,

both experimental and design, primarily because they contribute

negatively to the accuracy of test results. Unfortunately,

conrtlete randomization fails to isolate or equalize individual

plot variations. That has the possible effect of biasing the

data in favor of one or another treatment effect. A way of

eliminating this problem is to have large enough samples so

that individual differences will tend to average out and the

plots can be considered to be homogeneous. The solution

sounds easy but in reality the researcher faces obstacles

that for the most part are insurmountable. The most crucial

ones are cost and time considerations for accomplishing the

experiment, and the usually limited resources available from

which to draw experimental units. So, ultimately upon judging

the various considerations, the completely randomized design

27

is most appropriate where units under observation are homogeneous

or where the accuracy is good enough to overcome the effects

of variation error. Otherwise, it seems that an alternative

design is required to obtain satisfactory experimental results.

Randomized Block Design

Both Cochran and Cox (13:107), and Finney (16:51)

agree that the most frequently used of all experiment Jesigns

is the randomized block. This design is based on a principle

of assigning individual plots to blocks so that the plots

within each block are more homogeneous. The differences among

the blocks are then considered as nuisance variables that are

essentially isolated through the experiment design. The plots,

in this case, are not randomly selected from the sample

population but are grouped for ho-nogeneity. Randomization is

restricted within the blocks to assignment of treatment levels

for individual plots. The basic design layout is shown in

Table 2 with the symbolism essentially the same as for the

completely randomized design. The "X. symbol now indicates1J

a block level plot interacting with a random treatment level

and the symbol "X." is added which represents the mean of

summed block effect data.

28

TABLE 2

RANDOMIZED BLOCK DESIGN LAYOUT

1 T2 T

Block (1) X X X X11 12 lj l

Block (2) X X X21 22 2j

Block (i) Xil X i2 xi X'

1 X.2 x. j

Looking at the layout in Table 2, the differences

among the column means (5..) represent treatment effects

whereas the differe es among the row means (Xi.) represent

block effects. member that the block effect indicates

differences in'he criterion or dependent variable due to pre-

selected variations among the plots. The analysis is fairly

straightforward and employs the two-way (treatment and block

effects) ANOVA. With this design two test hypotheses can be

investigated. Not only can possible treatment effects be

looked at but also effects of plot variations can be studied.

The main objective however, is usually to test for treatment

differences.

29

The major advantage of this design over a completely

randomized one is that it provides some control over the error

effect. This is accomplished by avoiding total random assign-

ment of plots to treatments. The testing of treatment effects

becomes more valid due to the reduction of experimental error

based on individual plot differences. In using a design that

has the property of being able to reduce the error variance,

the researcher can expect a more precise estimate of treat-

ment effects. Thus, the randomized block design is more

powerful than the completely randomized design if, in a

particular experiment, block effects account for a significant

portion of the total error variance. Here again though, the

experimenter must weigh the added complexity of matching plots

against the possible gain in precision. Quite possibly, the

degree of precision is still not satisfactory and the search

for other alternatives must go on.

Latin Square Design

When a researcher feels that two uncontrollable vari-

ables within plots represent major sources of experimental

error then the possible use of a Latin square design is

indicated. This design evolved from an ancient puzzle which

involved finding the number of ways Latin letters could be

arranged in a square table so that each letter appeared only

once in each row and column. The blocking principle, as used

30

in the previous design, is extended in this design to achieve

homogeneity among two so-called nuisance variables. The two

variables are assigned in block levels to rows and columns

of a square matrix whose size is determined by the number of

/treatments under investigation. Each treatment is randomly

assigned to a cell within the square under two restrictions.

Each treatment can appear in any row only once and in any

column only once. Table 3 shows a Latin square layout for a

case with three treatments or levels. The symbolism used is

defined as follows:

A. = First uncontrolled variable levelI

B. = Second uncontrolled variable levelI

Tk = Treatment variable or level

Xijk = Cell data point (random treatment Tk interacted

with block A. and B. levels)2. J

X... = Mean of summed data for A.11

X. ,. = Mean of summed data for B.J 3

X''k = Mean of summed data under Tk

Note: To achieve a complete Latin square design there must

be equal numbers of blocks and treatments.

31

L .... ...- .. ... .. . ..J

TABLE 3

LATIN SQUARE DESIGN LAYOUT (3X3)

Block (BI) Block (B2) Block (B3 )

T1 T2 T3

Block (A1 ) XI1'"Xill

X122 XI33

T 2 T3 T1

Block (A2 ) XX23X2"X222 231 2

T 3 T1 T2Block (A3) X"X313 X32 1 X332

X.1. . .

X.. = (Xill + X321 + X231)/3

X''2 = (X2 1 2 + X122 + X332)/3

X'. = (X3 13 + X22 3 + X133)/3

From Table 3, the differences among the row and column

means, (Xi..) and (R. j.) respectively, represent two different

block effects. The differences among the means derived from

the calculations in Table 3 (R.. k) represent treatment effects.

The basic analysis used to test the two block hypotheses and

one treatment hypothesis is simply an extension of the ANOVAs

described previously7 however the primary interest is still

with evaluating the treatment effects. With proper planning

32

_ _ _ _... - ., - '

in the choice of variables to be blocked some of the effects

of unwanted variation can be avoided. This does not totally

eliminate the concept of randomization since, in the proper

use of this design, treatments are randomly selected as stated

earlier. This selection is accomplished by randomly choosing

from all of the possible Latin squares of a particular size.

A quick look at the limited data in Table 4, taken from

Finney (16:58), indicates that as the square size increases

the random possibilities become enormous.

TABLE 4

POSSIBILITIES FOR LATIN SQUARES

Size of Number of DifferentSquare Squares

2X2 2

3X3 12

4X4 576

5X5 161,280

6X6 812,851,200

7X7 61,479,419,904,000

The Latin square design has the overall effect of

reducing experimental error even further than the two previous

designs. A chief restriction on the use of the design is

that as the number of treatment levels gets larger the multi-

plicity of experimental trials necessary to satisfy differential

33

cell requirements becomes impractical. Here again, the

researcher must make a choice among alternative designs

based on the experimental environment he faces.

Incomplete Block Desiqn

A situation where an incomplete block design is

particularly applicable is when the available plots for block

levels turns out to be less than the number of treatments

being investigated. Another case would be if the number of

treatments was so large that to fill all the required blocks

would mean a significant loss of precision due to the hetero-

geneity of the plots. The formulation of this design requires

that each block have the same number of plots, each treatment

occur the same number of times, and plots be assigned to

treatments so that every possible pair of treatments occurs

together within some block an equal number of times. If the

symmetry described here is achieved then the design is

considered balanced; otherwise the design is partially balanced.

Of course, the closer the formulation can be made to total

symmetry the higher the precision of means tests will be. A

balanced incomplete block design layout for three treatments

is shown in Table 5. The symbolism used is the same as that

used for the randomized block design.

34

TABLE 5

INCOMPLETE BLOCK DESIGN LAYOUT (BALANCED)

T T T1 2 3

Block (1) XII - XI3 XI"

Block (2) - X X22 23 2

Block (3) X X - X31 32

Differences among row and column means can be compared

to determine block and treatment effects as in a randomized

block design. But to reach the point of analysis with this

design requires a high degree of computational dexterity.

The statistical analysis is far more tedious than in the

designs discussed previously. Initially what is required is

the solution of a set of linear equations whose number is

determined by the relationship (T + B - 1), where "T" is the

number of treatments and "B" is the number of blocks. The

computations then quickly become worse, so that is about all

this author is willing to say about the statistical analysis

at this point. Anyone wishing a more complete discussion is

referred to Cochran and Cox (13:380-384,443-463) for the

details.

A disadvantage to using this design is, in fact, the

cumbersome computations that are required. Also, there are

no formal procedures for accomplishing a symmetrical layout,

35

__ __

which makes it more difficult to construct the experiment.

If the researcher, due to resource considerations, finds it

necessary to use this approach then there are some benefits

to be derived. This design does permit the evaluation of

several treatments without the necessity of having complete

blocks. Also, the design can be more efficient than a

randomized block since the method of analysis gives not only

intra-block information but inter-block information as well.

Factorial Design

This methodology is actually not a particular design

but a number of techniques that combine other designs. A

brief discussion is felt to be important though because

factorial methods have gained widespread acceptance especially

in the area of behavioral research. The method makes use of

combinations of established building block designs to permit

the evaluation of the effects of two or more different treat-

ments simultaneously within a single experiment. Two of the

most commonly used designs have been discussed earlier. They

are the completely randomized and the randomized block metho-

dologies. A researcher might consider a factorial experiment

for two primary reasons. One, information concerning the

average effects of each of several different treatments can

be obtained from one experiment of moderate size. Two, this

method allows the researcher to assess interaction effects

among the treatment variables.

36

As in all things, there are advantages and dis-

advantages to selecting a factorial type of experiment. On

the plus side, if the treatments are independent of each

other, or their interactions can be considered insignificant,

then comparison of the main effect of each treatment can be

evaluated separately in the analysis. Also, one experiment

can provide information on several treatments whereas several

experiments with single treatment variables would be required.

On the negative side, if the treatments are numerous then the

size and complexity of a single factorial experiment can

become most unwieldy. If interaction effects are strong then

the analysis will be more complex because those effects must

be accounted for in any ANOVA procedure. The interpretation

of the results becomes more difficult because of treatment

interactions.

Ultimately, it is the responsibility of the researcher

to make an evaluation early on as to what is required to

accomplish an experiment with satisfactory results. The

approaches described here are only the very basic ones

necessary for a cursory look at the subject. They can be

combined and modified almost ad infinitum to suit any number

of experimental environments. A key point to note is that

an "expert" statistician can be of immeasurable help in

determining what experiment design to follow since, in the

end, it is the statistical analysis that will decide the

37

validity of the results. Also, randomization seems to play

some part in all of the basic designs discussed, as a

deterrent to biasing any data. As Finney (16:48) so eloquently

stated, -w hen in doubt, randomize."

This chapter has presented some background information

on the experiment design discipline; some basic terminology

has been described and defined; and the major building block

designs have been discussed to give some feel for the basic

approach to general experiment design. Armed with this basic

knowledge, Chapter III takes a look at the unique problems

arising in experiment design when human subjects are the

experimental units under treatment.

38

r II I "-- - .i- - -i- -

Chapter III

EXPERIMENT DESIGN WITH HUMANS

In Chapter II the subject of experiment design was

introduced. A number of historical points of fact were men-

tioned in relation to the development of the experiment

design discipline. Following that discussion, several terms

deemed basic to the topic were defined which led to descrip-

tions of five types of experiment designs. The choice of

particular designs was made based on a number of sources in

the field referring to them as basic building blocks to the

science of experiment design. With that as a basis, this

chapter will narrow the field of view somewhat and discuss

problems in experiment design validity as they typically

occur when humans are the experimental units under treatment.

3ackground

More than in any other type of research, when human

subjects are the units used for receiving experimental treat-

ments the difficulties that arise in attempting to achieve

valid test results increase in intensity. Probably the key

discriminator between experimentation in the "hard" sciences

(engineering, biology, agriculture, etc.) and those that

primarily focus on human beings is heterogeneity. What is

meant by that is, as experimental units, human subjects

39

exhibit an inherent multiplicity of diverse characteristics

which tend to maximize between subject differences; whereas,

in the "hard" sciences it is somewhat easier to achieve some

semblance of homogeneity between units subjected to experi-

mental treatments. This is so because it is much easier to

maintain uniformity when dealing with inanimate materials,

laboratory test speciments, chemical solutions, and the like.

What became apparent, through researching the litera-

ture for this section, is that there seemed to be vastly more

written about experimentation in the social/behavioral

sciences and education but not much in the area of human

subjects interacting with a physical task environment. Parsons

(33:1-2) however, in discussing the broader topic of man-

machine system experimentation, proclaims that there are

many characteristics in common with research in the behavioral

sciences. Another point he makes is that the man-machine type

of research is a hybrid of sorts and therefore is not claimed

by the more traditional researchers as their own. This could

possibly be a reason for the subject not being widely pub-

licized. At any rate, using this tack of a strong relation-

ship to behavioral studies, the following section concerning

human subject design problems draws heavily on two sources

from the behavioral area. The first is a survey of experiment

designs for teaching research by Campbell and Stanley (11)

which was initially published in 1963. The second is a text

by Walizer and Wienir (41), recently published (1978), dealing

40

with research methods for the behavioral sciences. Both works

contain fairly comprehensive treatments of experiment design

and validity, with the latter borrowing much from the former.

In point of fact, ;Aalizer and Wienir (41:242) refer to the

effort by Campbell and Stanley as ". the modern 'bible'

on experimental design." Since most of the material for this

discussion has been extracted from the two sources mentioned

above, specific citations will not be made unless quotes or

other references are used.

Experimental Validity

Webster (42:980) essentially defines validity as the

quality or state of achieving a conclusion that is correctly

derived from certain premises, or the state of being well

grounded. In the context of experiment design, validity

consists of two definable distinct concepts which are of

primary concern to a researcher attempting to achieve satis-

factory results. These two important concepts are internal

and external validity. Internal validity refers to the

criterion that, in fact, an experimental treatment is the

causal factor for a specific set of experimental conditions.

External validity refers to how extensively, beyond an

experimental setting, can a treatment effect be generalized

(11:5). The former term being the more critical of the two

will be dealt with first.

41

Internal validity is considered an indispensible

criteria and therefore an absolute necessity to obtain satis-

factory experimental results. Without internal validity it

is impossible to interpret any experiment to determine if a

treatment made a difference within the sample population. To

ideally achieve internal validity there are several extraneous

variables (those not related to any treatment variables) that

need to be controlled. The strong necessity for control is

that, if not controlled, the effects of the extraneous variables

can confound any treatment effects thereby confusing the test

results. Campbell and Stanley (11:5) give short definitions

of classes of extraneous variables as threatening to internal

validity. Walizer and Wienir (41:243-247), using a few

different titles, discuss similar classes of variables in

somewhat greater detail. The substantive material below

describes those extraneous variables as a synthesis from the

two sources cited above.

History Effects

Events that occur, in addition to the experimental

treatment, make up the history within a subject's experience.

The events other than the treatment may produce unwanted

history effects unless they are controllea by the researcher.

Basically, there are two ways this can be done. The first is

to totally isolate the experimental subjects so that the only

event experienced is the treatment under study. This method

42

_________ I

is impractical at best under most situations. The second is,

by judiciously choosing a suitable experiment design, to

negate the confounding effects of extraneous events.

Maturation Effects

There are many processes that may occur within

experimental subjects that are simply the results of a

temporal condition. Maturation involves the changes that

take place over time other than those related to historical

events. Some of these maturation effects that can contribute

to confounding are growing older, getting hungrier, becoming

fatigued (both physically and mentally), getting bored, and

so on. It is obvious from these examples that the time

period involved in the experiment is a determining factor for

the onset of each condition. So it behooves the researcher

to carefully consider a design choice in light of the length

of the experiment to be run.

TestinQ Effects

In research methodologies that make use of pretests

(measurements obtained prior to a treatment) and posttests

(measurements obtained subsequent to a treatment) the post-

test scores may be affected solely due to the fact that a pre-

test was given. If a measurement involves a type of perfor-

mance that tends to improve with repetition, then administering

a pretest provides an opportunity for practice and a likelihood

for higher scores, any treatment nonwithstanding. As Campbell

43

and Stanley (11:9) state, ' students taking the test for

a second time . . . usually do better than those taking the

test for the first time." An opposite effect, resulting in

lower posttest scores, is also possible if a pretest causes

fatigue, boredom, anxiety or other detrimental effects on a

subject.

Reactivity Effects

Campbell and Stanley do not treat reactivity as a

separate extraneous variable class but bring it up in relation

to their discussion of testing effects. Walizer and Wienir

however, do break out reactivity as a distinct source of con-

founding. It is being singled out here because reactivity

seems to be a confounding variable of significant concern in

the context of biofeedback experimentation. Reactivity effects

surface any time human subjects knowingly participate in an

experiment. The problem arises because subjects are aware of

their participation and therefore may react differently than

if they had received a treatment in a non-experimental setting.

A key point, as Campbell and Stanley (11:9) put it, is that

The reactive effect can be expected whenever thetesting process is in itself a stimulus to changerather than a passive record of behavior. ...In general, the more novel and motivating the testdevice, the more reactive one can expect it to be.

The way out of the dilemma is to use nonreactive measures if

possible. However, that likelihood is relatively remote. Only

if the experimental setting commonly occurs in the subject's

normal environment can the absence of reactivity effects be

assured.44

Instrumentation Effects

When using measuring instruments in an experiment,

the calibrations may change which will introduce an undetected

effect on a dependent variable measurement. This instrumenta-

tion phenomenon can also occur when human observers are the

"measuring instruments." In fact, the variability of a

human observer is probably greater and more likely to occur

than if mechanical instrumentation is used. Recognizing

that this effect will happen, it can be controlled by seeing

that any instrumentation or decay occurs equally among

experimental groups.

Statistical Regression Effects

In a pretest-posttest methodology where a researcher

is interested in studying subjects with extreme initial scores

the problem of obtaining unreliable posttest measures exists.

This is so because, as a statistical phenomenon, when multiple

measurements are taken scores tend to regress toward some

mean value. For example, if a group were selected for treat-

ment based on their extremely low measurements and then

retested, any observed increase may not have been due to the

treatment. Some of the initial low scores may have been chance

events so, on average, some increase would be expected to

occur simply due to the regression effect. Here again, the

proper choice of a design can control the possible confounding

of the extraneous variable.

45

'Selection Effects

The preferred method for controlling differences in

experimental subject's characteristics is through selection

by randomization to treatment and non-treatment groups. If

randomization is not done then a selection effect occurs which

obscures any possible conclusion that could be made from

observed differences between treatment and non-treatment

groups. The selection effect is based on the subject's

characteristics, in each experimental group, being the cause

for the observed difference. In essence, each group is

different with or without any treatment and attempting to

equalize groups by matching characteristics is not considered

sufficient. The problem with that approach is that it is

always possible for a researcher to neglect an important

matching characteristic or conversely, to match subjects

based on some insignificant ones.

Experimenter Bias Effects

Walizer and Wienir (41:247) single out experimenter

bias as an extraneous variable with a strong influence on

confounding. The effect occurs when an experimenter, either

knowingly or by chance, somehow influences a subject's response

in an experiment. Bias can also result when an experimenter

has knowledge of the hypothesis being tested and/or which

subjects are members of treatment or non-treatment groups.

There are a number of techniques commonly employed in an attempt

46

to reduce the effects of experimenter bias. These include

such methods as: (1) having the persons responsible for

giving instructions or taking measurements ignorant as to the

hypothesis under study, (2) insuring that the same persons

in (1) above also are not aware of which subjects are in treat-

ment or non-treatment groups, and (3) using automated devices

to record data whenever possible. The first two methods are

usually expressed as the experimenter being "blind" to the

hypothesis and/or subject manipulation. Anyone wishing to

explore this subject further is referred to Rosenthal's (35)

expansive text titled Experimenter Effects in Behavioral

Research. Also, the other side of the coin (subject bias)

is treated in depth in Rosenthal and Rosenow's (36) book The

Volunteer Subiect.

Subject Mortality Effects

When there is a differential loss of subjects in a

comparison group experiment, or a loss of subjects in a single

group pretest-posttest design, mortality confounding effects

are possible. There are a multitude of reasons for such

losses including illness, moving, or just plain not showing

up. Rosenthal and Rosenow (36:23-25) discuss the issue of

subjects not appearing for appointments and such individuals

are referred to as "pseudovolunteers," a term coined by other

researchers (apparently, it seems, researchers feel better

when phenomena are given neat little names). When mortality

effects occur, differences in measurement means after a

47

-

treatment may be due to the loss of subjects whose individual

differences affected pre-treatment measurements. There is no

! L ideal way to protect against this extraneous variable regard-

less of the type of experiment design being used. The best

a researcher can do, when faced with a differential loss of

subjects, is to see that the perceived important individual

characteristics of the remaining subjects are balanced.

In addition to the specific variables relevant to

internal validity, as discussed above, there are combinations

of effects. These are somewhat more obscure and involve

interactions between selection effects and others mentioned

above such as maturation, testing and history. Should all of

the sources of confounding be ideally controlled then an

experiment is considered internally valid; however, the experi-

menter must also be concerned with external validity as well.

To what population, outside of the subjects measured, can a

treatment effect be generalized? This is a more nebulous

concept to consider as compared to internal validity.

Generalization or representativeness of an experiment involves

being able to infer that what happens to a sample population

can be extended to some larger population. As in internal

validity, there are several factors that can jeopardize

external validity and these will be discussed here.

48

_ . , mihad .~

Testing and TreatmentInteraction Effects

An experiment design that involves a pretest measure

may present a threat to external validity due to a testing

and treatment interaction. The effect occurs because, in the

"real" world, measures taken from subjects to establish a

baseline tend to affect their response to a treatment variable.

As a result posttest measures are not representative of any

possible treatment effect on the population under investiga-

tion. Controls for this effect may be achieved by either

eliminating the pretest measure entirely or by choosing an

experiment design that will account for the anticipated

confounding variable.

Selection and Treatment

Interaction Effects

The selection of subjects is an important considera-

tion for both internal and external validity. To achieve

internal validity the preferred method is to randomly assign

subjects to treatment groups; however, if the researcher is

interested in a specific population group this presents a

problem for external validity. The subject groups selected

in this manner eliminates any guarantee that they are

representative of any particular group of interest. To

eliminate this effect randomization of subject selection must

occur from all individuals in a population of interest. This

49

LI

is very difficult to achieve due to considerations such as

geographical location, subject population availability, and

time and cost factors.

Experimental Arrangement Effects

One of the most difficult dilemmas to try and resolve

is whether or not experiments in a controlled or natural

setting produce the best results. In many cases this may be

a moot point due to the nature of the treatment under investi-

gation requiring complex instrumentation and controls. A

natural setting tends to increase external validity but

extraneous variables are more difficult to control thereby

threatening internal validity. In any event, internal

validity, being the more critical of the two, should not be

sacrificed to satisfy external validity. If at all possible,

conducting like experiments in both settings would allow a

determination of whether or not results are obtained on the

basis of arrangement effects alone.

Multiple-Treatment Interference Effects

Typically, in experiments where a single group of

subjects are presented with multiple treatments, the results

are representative only to an overall population in terms of

the same sequence of multiple treatments. This happens

because, in general, the effects of one treatment do not

50

disappear and therefore have some residual effect on the

results of another treatment. The resulting interference

effect clouds the evaluation of each treatment with respect

to its generalizability to other than the sample population.

It is evident from the discussions above that in

order to obtain valid test results the sources of confounding

and the factors affecting generalization must be considered

very carefully. With that in mind, the next section will

discuss some experiment design methodologies in behavioral

research and how they relate to experimental validity.

Human Subiect Experiment DesiQns

In Chapter II the point was made that the number of

different design approaches was almost limitless. Here too,

in an area where the researcher has to concern himself with

not only a multitude of experimental situations but also the

idiosyncrasies of human behavior, the design possibilities

are limited only by the researcher's inventiveness. Campbell

and Stanley chose a limited number of designs and most expertly

discoursed on the nature of each design; and how it either

satisfied or did not satisfy both internal and external

validity factors. To reiterate all of their work here would

be a pointless waste of time since they sail it better and

with more knowledge than this author ever could; however it is

important that the reader get a feel for how validity factors

do interact with experiment designs.

51

Campbell and Stanley divided the designs they discussed

into three groups as follows:

1. Pre-Experimental designs that suffer more, in

relation to other designs, by not being able to satisfy many

of the validity factors.

2. "True" experimental designs that are the ones

most recommended in much of the experiment design literature.

3. Quasi-Experimental designs that exhibit a lack of

complete experimental control over such things as randomiza-

tion of human subjects and the scheduling of treatments.

One experiment design of each category will be presented out

of Campbell and Stanley's (11) treatise as sufficient material

to get at the crux of the issue in this section. Should the

reader wish to investigate this topic in greater detail the

original text is the recommended source.

Before proceeding with the experiment design discussion,

there are some symbols that require definition and the design

layout convention as presented in Table 6 needs to be addressed.

The symbols used are defined as follows:

X = Represents exposure of a subject or group of

subjects to a treatment variable whose effects

are to be measured

0. = Represents an observation or measurement process

to gather data for evaluation of treatment

effects

52

R = Represents the randomization process of

assigning subjects to different treatment

groups as the method of achieving pre-treatment

equality

Each design layout is to be read from left to right indicating

the temporal order of events. Any symbols that appear

vertically oriented indicate that those events occur

simultaneously.

One-Group Pretest-Posttest Design

A pre-experimental design that is still used in

educational research, despite its faults, is the one-group

pretest-posttest. The design layout is shown in Table 6.

The design's simplicity and the possibility that no other

alternatives exist are the most likely reasons for its use;

however, several rival hypotheses, concerning extraneous

confounding variables, become viable explanations of an

01-02 difference. Validation of a treatment effect hypothesis

which states that "X" is the cause for the difference is

definitely a problem here, and how this design's results are

confounded by extraneous variables will be taken up next.

53

______________

Table 6

EXPERIMENT DESIGN LAYOUTS

One-Group 0 X 0Pretest-Posttest 2

R 0 X 0Pretest-Posttest 12Control Group R 0 0

3 4

Nonequivalent 1 2

Control Group 03 04

Events that occur, other than "X," between the 0 1-O2

measurements rival the test hypothesis as producing the change.

A key point is that this history effect will decrease the

validity of the results as the time lapse between the two

measurements grows longer. Experimental isolation is a curebut in the human behavioral arena it is practically impossible

to achieve. Maturation effects are also a problem, independent

of external events. In this single-group design no distinction

can be made between the internal temporal processes of sub-

jects and the treatment variable when trying to determine a

causal relationship for a measurement difference. Testing

effects confound the results as explained in the previous

section. The pretest itself then, most likely affects the

posttest measurements and becomes a rival hypothesis for any

54

measurement change. Along with testing effects reactivity

to the pretest measure can also influence the posttest scores

adding to the confusion.

Instrumentation effects are another cause for the

lack of control when using the single-group pretest-posttest

design. Changes in the measuring device may account for a

detected 01- O2 difference. The effect is more likely when

human observers are the means for measurement; however, when

automated equipment is used the effect is still present in

calibration errors. Regression effects, as discussed earlier,

are a hazard in this design when subjects are chosen for a

treatment specifically because of the extremity of their

pretest measurements. A change in measurement means can be

mistakenly attributed to "X" when in fact the extreme pretest

scores have simply regressed naturally toward the mean. It

is apparent, from this discussion, that this experiment design

leaves a lot to be desired. In fact, this design does not

conform to any of the Aajor building block designsdiscussed

in Chapter II. Each of the building block designs generally

require more than one treatment group for comparative analysis

whereas this design deals with a single group and a single

treatment mode.

Pretest-Posttest Control Group DesiQn

In an effort to control the confounding effects of

extraneous variables affecting internal validity, a control

55

group can be added and equivalence of groups achieved through

randomization, resulting in the pretest-posttest control group

design. The layout of this"true" experiment design is shown

in Table 6. This methodology is one of the most frequently

used and is called the '. classical experimental

design . . . by Walizer and Wienir (41:231) who go on to

say that it ". . is considered the grand master of research

designs because in a relatively simple way the researcher can

deal with many of the problems of demonstrating causation .

This design conforms to the completely randomized design, as

discussed in Chapter II, where it is possible to randomly

select subjects for different treatments. History, maturation

and testing effects are all controlled through being manifested

equally in both the treatment and non-treatment groups. Care

must be taken to avoid intrasession history effects caused by

simultaneous experimenter differences. To achieve a balanced

representation for this and other biases randomization of

experimental occasions should be followed if possible. A

point to be made here is that the design, using an experimental

group receiving "X' versus a control group receiving no 'X,"

is an oversimplification. The control group may in fact be

experiencing other levels of "X" or a different set of

activities altogether which in reality adds some ambiguity

to any evaluation of the effect ol "X."

56

Regression and selection effects are essentially

controlled through the randomization process assuring group

equality. In the case of regression, if both treatment and

control groups are randomly selected from the same extreme

population then they should equally regress toward the mean

on posttests. Thus, the O1-O2 difference can still be

related to the application of "X alone. Selection effects

are ruled out by the same randomization of the subject groups;

however, a proviso here is that true random samples based on

statistical probability must be achieved. The larger the

number of random assignments from an overall population the

greater the assurance of group equality.

Instrumentation effects are easily controlled if

intrasession history effects can be controlled; however, the

problem is more difficult if observers are the instruments of

measurement. The types of controls needed then, are those

mentioned in the last section under the heading of experimenter

bias effects. Mortality effects are controlled by the nature

of the data collected within the design framework. When sub-

jects in either experimental or control groups drop out, valid

inferences about a O1-O2 difference can still be accomplished.

This is done by retaining data for analysis from all subjects

that have completed both the pretest and posttest. The

apparent effect of "X" may be reduced but it does eliminate

differential sampling bias. The pretest-posttest control

57

group design does a good job of controlling extraneous

variables to give it internal validity; however, there are

some concerns when the discussion turns to external validity.

The previous section pointed out that achieving

external validity is somewhat more difficult than achieving

internal validity. The hazards discussed there play a definite

role in affecting the external validity of the pretest-posttest

control group design. The pretest makes a testing and treat-

ment interaction a strong possibility unless the nature of

the testing is familiar and is seen frequently by the experi-

mental subjects. Where highly unusual test procedures are

employed it might be wise to choose an experiment design that

does not contain a pretest. A selection and treatment inter-

action is also a strong possibility unless the tested subjects

are able to be randomly selected from the entire population

under study; otherwise, the results may only be valid for the

specific groups measured. By far, the most pervasive of all

threats to generalization is the experimental arrangement

effect. Because of the very nature of experimentation, most

attempts to control significant variables leads to an artificial

setting. Regardless of the type of design, reactive effects

are unavoidable unless some semblance of a natural setting can

be achieved.

The "classic"pretest-posttest control group design

does exhibit some difficulties with satisfying generalizability;

however, as stated earlier, being internally valid is of

58

sufficient importance that its relevance to experimentation

is still maintained. As good as the design is though, a key

point is the requirement for randomization of subjects. On

many occasions this is not possible and "untrue" designs must

be used to accomplish the necessary research. One such experi-

ment design and its relationship to validity will be explored

next.

Nonequivalent Control Group Design

Quasi-experimental designs are used where designs

that have a better "track record" in achieving validity are

not feasible. It should be remembered, as discussed in

Chapter II, that there are always risks in the testing of

hypothesis. While these risks are somewhat greater in the

quasi-experimental versus "true" designs they are still worthy

of consideration. The researcher simply must be more wary of

threats to validity when interpreting the results. The non-

equivalent control group design is of the quasi-experimental

variety and is widely used in educational research. As

indicated in Table 6, it is similar to the "true" pretest-

posttest control group design but the experimental subjects

are not necessarily assigned randomly to the comparison groups.

With a design of this type, the usual method used to achieve

comparability of subject groups is to match them based on

59

individual attributes. A methodology similar to this one was

described in Chapter II as the randomized block design. The

dashed line represents comparison groups that are not equated

by randomization.

History, maturation, testing, and instrumentation

effects are controlled in a similar fashion as in the "true"

design discussed previously. The degree of control is some-

what determined by how similar the treatment and non-treatment

group are, based mainly on the similarity of pretest measures.

The distinguishing internal validity factor of this design

versus the "true" design is the threat of selection interactions

with other extraneous variables. The lack of randomization in

the selection of comparison groups may cause an O1-O 2 difference

that could be mistaken as the effect of "X." Regression

effects are also a problem with this design because of

inevitable differences in pretest group means, again due to

the lack of randomization.

Though a few problems to internal validity were noted

above, this design does fare a little better in controlling

for effects that threaten external validity. The problems

encountered in this area, for the most part, are similar to

those presented in the discussion of the pretest-posttest

control group design. Reactive arrangement effects however,

are not as likely to threaten external validity in this

design as in most "true-designs. The reasoning is that

60

where random selection for treatments is not used, naturally

occurring groups of subjects are less likely to be aware of

experimental manipulations.

The material presented in this chapter included a

short background section containing some general comments

concerning experiment design with human subjects; a discussion

of factors relevant to internal and external design validity;

and a description of three experiment designs and their

interactions with threats to validity. Admittedly the

brevity of the treatment does not do the subject justice;

however, it is felt that the intent, to acquaint the reader

with the complexity and difficulty associated with experiment

design validity using human subjects, has been served. With

Chapter II and this chapter as a foundation, Chapter IV looks

at some of the literature involving biofeedback experimentation

in the area of task performance enhancement.

61

Chapter IV

BIOFEEDBACK EXPERIMENTATION AND

TASK PERFORMANCE

In the introductory chapter the question posed was,

can task performance be improved using biofeedback control?

The results of Kipperman's research was inconclusive and

therein lay the purpose for this study. Chapter II dealt

with areas of concern in the field of general experiment

design. Chapter III narrowed the discussion to concerns

where human subjects are the focus of experimental treatments.

Both chapters have hopefully laid a foundation for an

appreciation of the inherent complexities involved in devising

a valid approach to biofeedback experimentation. This chapter

looks at available literature involving biofeedback experi-

mentation and any relationships those studies might have

with respect to the Kipperman experiments, and suggests possible

alternatives.

Background

In Chapter I, the point was made that most of the

published material in the area of biofeedback concerns clinical

research and applications. Though a couple of research reports

62

dealing with task performance were unearthed in the search,

not a single reference was found relating biofeedback to

performance in a non-clinical sense. On the clinical side,

a number of books have been published geared to the public at

large. These include Brown's (7: 9) popular works New Mind,

New Body and Stress and the Art of Biofeedback; and Blanchard

and Epstein's (6) A Biofeedback Primer. In the professional

arena periodicals, such as Biofeedback: Research and Therapy

and Biofeedback and Self Regulation, have long been established

to report on biofeedback research and applications. The

stature of biofeedback as an applied science has also made

inroads in the medical profession. This is evidenced by the

inclusion of works by Gaarder (19) and Basmajian (2) in the

Wright State University School of Medicine library. Both books

relate procedures and practices for the clinical use of bio-

feedback techniques. Because of this proliferation of work

in the clinical area, most of the information presented in

this chapter, of necessity, draws heavily from thoseefforts.

Here again, as discussed in Chapter II, the problem

of what material to present had to be broached. The reader,

using the bibliography as presented, could certainly gain

more detailed information by going directly to the sources.

Thus, the approach taken was to selectively discuss material

that would whet the reader's appetite and at the same time

relate to the Kipperman experiment. In that light, the next

63

section looks into biofeedback research as a scientific tool

by including some general experiment design approaches.

General Biofeedback Experimentation

Biofeedback, as a valid scientific mechanism for

promoting voluntary physiological changes, has been a long

time in coming. Historically, there has always been a

reluctance on the part of some to accept methodologies that

smack of control especially when instrumentation equipment is

involved. As examples, vocal resistance was strong when

B. F. Skinner's pioneering work on behavior modification

emerged, and some misunderstood the meaning of control as

forwarded by Norbert Wiener when he proposed the now heralded

cybernetic theory of systems (38:2). As a result, researchers

shied away from investigating control of internal processes

using instrumentation. Also, as mentioned in Chapter I, there

were many who believed that the autonomic nervous system

would not be responsive to voluntary operant conditioning.

Over the last two decades the opposition to biofeed-

back, as a science to be reckoned with and not a "fad" cure

for all ills, has worn away as greater numbers of respected

researchers entered the field. While there are still questions

as to the efficacy of some of the methodologies employed,

there can be no question that, at least in the clinical area,

there are definite benefits to be derived from the use of

biofeedback. With this in mind, in 1974 Blanchard and

64

Young (5) wrote an excellent review of published reports on

clinical applications of biofeedback training employing various

methods of feedback. Their study revealed a wide diversity

of experimental procedures in use which they categorized

into several groups. They professed, what was likewise stated

earlier in this thesis, that the validity and reliability of

conclusions concerning treatment effects hinges on the ability

of an experiment design to control for extraneous variables.

Short summaries of Blanchard and Young's (5:4-6) groupings

are presented below to give the reader the gist of the types

of experiment designs most often used in biofeedback research.

They are described in the order of their ability to promote

increasingly valid results.

Anecdotal Case Report

The weakest of all experimental methods reported is

the anecdotal case report. No systematic collection of data

is used but some description of a subject's clinical symptoms

before and after the administration of a treatment is recorded.

Also, some information is kept concerning the treatment itself

and how it is applied to the subject. The value of this

design lies not in its ability to produce valid conclusions,

since it fails to control for most of the confounding variables

discussed in Chapter III, but in its simplicity which allows

for a minimum of effort and may suggest positive directions to

take in accomplishing more rigorous research.

65

Systematic Case Study

A design somewhat better than the previous one

described is the systematic case study. Here, data are

collected through systematic measurement from a pre-treatment

or baseline condition and several experimental or treatment

trials. This design also suffers from a lack of control for

several extraneous variables; however, with certain conditions

it can yield acceptable results. These include the establish-

ment of lengthy baseline data and experiencing a change in

the symptom of interest that is coincident with the application

of the treatment. While not a "true" experiment design,

increased validity can be obtained through replication with

several subjects. If similar treatment effects occur at

approximately the same point in the trials then additional

evidence for the efficacy of the treatment can be inferred.

Controlled Single Subject Experiment

A stronger design which uses an analysis of behavior

is the controlled single subject experiment. Data are

systematically collected across a minimum of three conditions.L

These consist of baseline, treatment, and return to baseline

measurements. The return to baseline or reversal effect, as

it is referred to, is considered the critical step. If a

symptom change occurs with the application of a treatment and

then returns to a baseline level when the treatment is

removed, then evidence exists that the treatment is a causal

variable for the symptom change. To increase the evidence

66

further, the treatment can be applied again to test for a

second similar symptom change. Again, without many of the

contrcls mentioned in Chapter III, any evidence gathered

must be treated with caution.

Single Group Outcome Study

A common design approach, due to its simplicity, is

the single group outcome study. Measurements of a target

symptom are obtained from a similar group of subjects both

before and after a treatment. Problems associated with a

design of this type were discussed previously; therefore, the

reader is referred to Chapter III where the information can be

found under the One Group Pretest-Posttest Design heading.

Controlled Group Outcome Study

The most effective design represented in the biofeed-

back research literature is the controlled group outcome

study. This design has also been discussed in Chapter III in

two forms as the Pretest-Posttest Control Group ("true")

Design and the Nonequivalent Control Group (quasi-experimental)

Design. Although Blanchard and Young use Campbell and Stanley

as a reference, their discussion of this design does not make

the important distinction of randomization. They simply refer

to the design as requiring a minimum of an experimental

(treatment group) and a control (non-treatment) group of

comparable subjects measured at the same time.

67

A modification of the controlled group design, and

probably the least used due to its complexity and difficulty

of operability, is the three group controlled experiment

design. In addition to treatment and non-treatment groups

an attention-placebo control group is added. Placebo is

defined in Stroebel and Glueck (40:20) as " any medication

(treatment) used to alleviate symptoms, not by reasons of

specific pharmacologic action, but solely by reinforcing the

patient's favorable expectations from treatment." In a

clinical environment, where therapy is administered to effect

a change in a target symptom, placebo or expectancy effects

are strong confounding variables which must be controlled.

This has been a well known fact in drug or psychological

therapy research and certainly extends to the area of bio-

feedback experimentation.

Blanchard and Young's review of biofeedback research

studies included, in the main, those that used EMG, heart rate,

blood pressure, or electroencephalogram (EEG) as the feedback

methodology. In summary they concluded, based on the soundness

of the experimental procedures employed to yield meaningful

clinical results, that EMG feedback methods yielded the most

valid results (40:34). Based on this study, at least

empirically, the choice of EMG feedback in the Kipperman experi-

ment was a good one. With the preceding discussion as a base,

the next section focuses on a few selected biofeedback studies

to provide a look into some methodologies that have been used.

68

Biofeedback and Performance

A synopsis of two experiments and one long-term study

concerned with different aspects of biofeedback research are

presented below. The first experiment deals with the effects

of relaxation training on mental performance under stress.

The second experiment deals with the theraputic effects of

EEG and EMG feedback for symptom reduction during detoxifica-

tion from a methadone habit. The long-term study is concerned

with several biofeedback modalities and their possible use in

enhancement of human performance. The three bodies of work

were selected to point out ramifications with respect to

experimental validity and to serve as an aid in judging the

efficacy of the Kipperman experiment.

Relaxation Training and

Performance Stress

Chaney and Andreason (12:677-678) wished to determine

the effects of a program of Jacobsonian progressive relaxation

techniques (using specific voice instructions) on performance

in a memorization test while under induced stress. Both

galvanic skin response (GSR), a measure of skin electrical

conductivity, and EMG feedback were used as dependent measure-

ment variables of interest throughout the experiment.

Forty-eight female student subjects were divided into matched

triplet groups based on th following data: (1) college

scholastic aptitude test scores; (2) Taylor anxiety test scores7

(3) EMG masseter (lower jaw) muscle baseline tension levels7

69

(4) pretest memorization task tension levels; and

(/ memorization task scores. Five one-way ANOVAs, performed

on the matching variables, indicated no significant differences.

The inference was made therefore, that each triplet was

reasonably homogeneous prior to the experimental treatments.

The triplets were then randomly selected for three possible

treatments as follows:

1. A control group in which the subjects received

no treatmen for reducing tension but participated in a

program of body mechanics.

2. An attention-placebo control group in which the

subjects received a placebo pill daily that supposedly

reduced tension.

3. The experimental group in which the relaxation

techniques were taught with EMG visual and auditory feedbe--

to monitor the progress of relaxation control.

All groups received six weeks of their respective

treatments at which time a posttest was administered along

with an induced stressor. A threat of academic grade point

failure wa.; made if no improvement was shown in the posttest

versus pretest merorization scores. Quantitative measures

were obtained on the same five variables used on the pretest,

and ANOVA techniques were basically used in the analysis.

The results indicated a significant difference in EMG levels,

on the posttest, between the no treatment control group and

70

the experimental group; however, no significant difference

was detected between the no treatment control group and the

placebo group. The inference made was that the relaxation

training group was able to control neuromuscular tension

better than the other control groups when exposed to a stress-

ful situation. Analysis of the memorization test scores

indicated similar results although they were not quite as

statistically convincing.

On the surface this experiment appears to be well

thought out. The methodology used is a randomized block with

a modification of the nonequivalent control group design

:"scussed in Chapter III; however the threats to validity

re not discussed by Chaney and Andreason as part of thelr

Le~ults. The lack of randomization leads to selection inter-

a,_t-on effects and regression effects due to the use of

Iathing. Both could have a causal effect on differential

posttest measures instead of the experimental treatment.

Kipperman (26:6) assumed randomization when in fact, with the

limited number of subjects available, it was not possible.

Matching on subject attributes was required to obtain some

comparability of treatment groups. It would seem then, that

the same threats to internal validity were probably present.

Experimenter and subject biases are a problem in the experi-

ment discussed here and in the Kipperman study. Differential

treatments used for both experiments were readily apparent to

71

both the researcher and the subject; therefore, biases for

the successes or failure of one treatment or another are

inevitable and become a detriment to validity.

As mentioned earlier, a placebo effect can be a

strong confounding variable when human cognitive processes

are at work. This factor was not addressed in Kipperman's

work except in a passing concluding comment. Kipperman

(26:41-42) remarked that " people are different

One cannot expect different individuals to react the same

way to the same situation . . . that fact must be incorporated

in any analysis of experimental results." Even before analysis,

individual differences need to be looked at in terms of the

experiment design itself, controlling for not only placebo

effects but bias and selection effects as well. Chaney and

Andreason attempted to control for this effect but the

methodology seems faulty. It seems, to this author, that to

effectively control for placebo effects the researcher must

be able to simulate the actual experimental treatment being

tested. The difficulty in accomplishing this, when relaxa-

tion training and biofeedback is involved, is explored in the

discussion of the next experiment.

72

A Double-Blind Methodology

Cohen, et al. (14:603-608) investigated the possible

theraputic effects of EMG biofeeback for reducing the symptoms

associated with detoxification from a methadone habit. With-

out going into the details, the results of their initial

research, where both the experimenter and subject were aware

of the treatments given (non-blind research), were less than

conclusive. Many of the subjects who did not "learn" the EMG

technique of tension reduction, based on collected EMG data,

nevertheless were successful in reducing their detoxification

symptoms. An apparent success bias was operating indicating

a need for an attention-placebo control for this effect. That

is easier said than done! Two major obstacles stand in the

way of accomplishing the task. First, how do you keep the

experimenter blind as to which subjects are receiving true or

simulated feedback when the experimenter must be intimately

involved with the biofeedback training procedure? Second,

how do you present simulated feedback to the subjects, that

will be essentially indistinguishable from true feedback? How

this double-blind experiment design was ingeniously accomplished

by Cohen, et al. in their second phase research is discussed

next.

An additional group of subjects received simulated or

actual biofeedback under the following test conditions:

73

!"

1. Pre-constructed tapes of EMG feedback were obtained

from subjects who, based on data in phase one, successfully

accomplished tension reduction.

2. A tape recorder was connected to a computer and

punch-card reader which was, in turn, hooked to the biofeed-

back apparatus. The system was set up so the computer could

discriminate punch-cards which would allow either activation

of the pre-recorded feedback tape, or actual real time feed-

back to be heard by the subject.

3. The experimenter's feedback display always indicated

actual real time subject responses, regardless of which mode

the subject was receiving.

4. The punch-cards, that controlled the treatment

selection, were randomly distributed to the subjects who fed

them into the card reader at the start of each trial.

With the above experimental controls instituted, the

major difference between the control and experimental groups

was the administration of real time or simulated feedback.

Debriefings of both experimenters and subjects revealed that

either group had no better than a chance probability of

determining which treatment was being used. Analysis indicated

that active biofeedback subjects in both the non-blind and

double-blind phases were equally effective in achieving

"learned" EMG tension control; while, little or no learning

was achieved by the placebo subjects in phase two. The

74

success rate for reduction of detoxification symptoms however,

was approximately equal for both the real time and simulated

feedback groups. The results indicate a very definite

suggestion that a placebo effect was a contributing factor.

Cohen, et al. did caution others though, that the experiment

was done under strict conditions with a very defined specific

population and the research should therefore not be construed

as valid for other clinical purposes. Of primary significance

though, is the demonstrated feasibility of a double-blind

technique within the severe constraints of biofeedback research.

There is a potential here, given the necessary resources, for

use in other situations such as the type of task performance

experiment attempted by Kipperman.

A Five-Year Research ProQram

A computer search of the Defense Documentation Center

files, relating to biofeedback research, turned up one study

(3) concerned specifically with biofeedback as an aid to human

effectiveness. The same study was reported on by Lawrence and

Johnson (28) under the title Biofeedback and Performance. The

five-year research effort, accomplished from 1970 through

1975, involved the efforts of 16 researchers. They performed

a number of experiments involving brain activity, cardiovascular

activity, muscle relaxation, and vasomotor activity. Their

goal was to evaluate whether learning self-regulation of

various physiological variables could enhance performance or

75

at least reduce performance loss under stressful situations.

The general charter given the researchers was: (1) to train

subjects to control various physiological variables, as

mentioned above, using biofeedback techniques; (2) to look at

correlations between the physiological variables and perfor-

mance tasks; (3) to induce some form of stressor to observe

its effect on the tasks, and (4) to determine if, through the

learned self-regulation process, performance could somehow be

enhanced. The experimental hypothesis tested in each case was

that individuals who learn to control their internal physiology

will perform better and have more control of behavior under

stress (3:3-4).

The experiments and detailed procedures accomplished

by the 16 researchers are far too voluminous to reconstruct

here. It will suffice to say that many of the experiments

involve fairly rigorous controlled conditions. The interest

here is the overall results that bear on Kipperman's findings.

Should the reader be interested in the details, a look at the

original study is recommended. Several emphatic conclusions

were arrived at upon the completion of the five-year study.

In a number of laboratory studies, learning to regulate some

internal physiological process through biofeedback training

was accomplished in most cases; however, it was difficult, if

not impossible, to alter the process to an endstate that was

contrary to an individual's best interest in regard to their

76

to their own physiology. This points to the fact that

individual differences play a large part in any form of bio-

feedback training or therapy, which makes generalization of

experimental results exceedingly difficult (3:20).

In general, the results of several of the induced-

stress experiments point to a lack of ability of subjects to

maintain control over previously learned physiological

responses when faced with a difficult task. The work accom-

plished in brain wave, heart rate, vasomotor, and EMG feed-

back indicated a lack of any significant relationship to

performance enhancement. At the end of these studies, as of

December 1975, the general opinion of the researchers involved

was that further efforts to discover a biofeedback-performance

link would prove fruitless (3:21-22). Kipperman (26:3-4) was

aware of the negative conclusions of the above studies when

he embarked on his experimental effort; however, the feeling

was that additional efforts in this area were still warranted.

His intent was to include more emphasis on learning and EMG

measurement to search for a relationship between tension

levels and performance. The experiment design however, did

not allow for any pretest measure of performance to establish

a baseline for the experimental and control groups. The

temporal environment perhaps forced a compression of the bio-

feedback leazning effort to coincide with the task learning

effort, thus introducing treatment interaction effects. These

77

items, coupled with the experiment design difficulties mentioned

earlier (placebo and selection effects; experimenter/subject

biases), probably contributed to the lack of significant

results in the Kipperman effort.

This chapter has presented a few background remarks

relating to biofeedback experimentation; a discussion of the

types of experiment design most often employed in biofeedback

research; and a few selected studies that helped to point out

some of the apparent difficulties in the Kipperman experiment.

To be sure, there are numerous accounts in the available

literature, especially in the clinical area, relating to bio-

feedback research; however, owing to the scope of this effort

the choice had to be limited. Chapter V, as the finale of

this thesis effort, briefly summarizes the material that has

been presented to this point and ends with some conclusions

and recommendations.

78

Chapter V

SUMMARY, CONCLUSIONS, AND RECOMMENDATIONS

Chapters II, III, and IV have hopefully led the

reader to recognize some of the important relationships

between experiment design in general, experiment design with

humans, and biofeedback experimentation. In the process,

these efforts were also intended to lead to evaluating the

lack of significant results of the biofeedback experiment

accomplished by Kipperman. This chapter presents a brief

summary of the preceding work, any conclusions drawn from it,

and closes with a few recommendations.

Summary

Chapter I introduced the topic with a discussion of

the developing interest in biofeedback research over the past

two decades. A discussion of Kipperman's experiment, which

attempted to relate biofeedback and performance, followed

pointing out the lack of significant results. The remainder

of the chapter was taken up with defining the objectives of

this thesis and the methodology to be followed. In the main,

the intent was to learn about experiment design and in the

process point out apparent problem areas with the Kipperman

research effort with the hope of suggesting possible improvements.

79

Chapter II discussed some background information, in

general terms, concerning the development of experiment design

as a science. Specifically, the work of R. A. Fisher was

singled out as the recognized pioneer in the field. Basic

terminology was defined and discussed as a requirement for

understanding the design descriptions to follow. Subsequently,

five experiment designs were selected and discussed for their

general treatment in the literature as the major building

blocks in the field. These designs included completely

randomized, randomized block, Latin square, incomplete block,

and factorial. The layouts and usefulness of each design

were presented to give the reader some idea of what is involved

in the various approaches.

Chapter III then narrowed the field down to experi-

ment design research involving humans as subjects. A back-

ground section related how the complexities of experiment

design increase when heterogeneous human subjects are used

versus the generally inanimate objects in the "hard" sciences.

Most of the literature relating to experiment design with

humans was found in the social/behavioral and educational

sciences. Experimental validity, both internal and external,

as major concepts for the success of any experiment were

discussed in some detail. Several effects, as threats to

either internal or external validity, were reviewed using

mainly the work of Campbell and Stanley as the source.

Finally, three experiment designsfor research with humans

80

were discussed as representative of distinct stages of design

effort. These stages are defined by Campbell and Stanley as

pre-experimental, "true" experimental, and quasi-experimental

designs.

Chapter IV, using the material presented in Chapters II

and III as a foundation, approached the main issue fostering

this effort. The area of concern, at the outset, was biofeed-

back and task performance and Kipperman's efforts to find a

relationship between the two. A few background remarks were

presented pointing out the relative lack of task performance

literature versus clinical literature in the area of biofeed-

back research. A discussion of several experiment design

techniques most often employed in biofeedback research

followed. These techniques ranged from the simplest anecdotal

case report to the most complex controlled group outcome study.

The last section included a synopsis of three studies selected

to aid in pointing out some apparent shortcomings in Kipperman's

experiment.

Finally, of course, this chapter brings to a

culmination the efforts presented up to this point. The

following conclusions and recommendations sections hopefully

indicate that the objectives initially expounded upon in the

introductory chapter have indeed been somewhat successfully

achieved.

81

Conclusions

As a result of the investigation undertaken for this

thesis several apparent shortcomings in the Kipperman experi-

ment were noted and may well have contributed to the lack of

significant results. These factors are enumerated below.

1. Selection effects are probable due to the lack of

randomization of subjects into treatment groups. Matching on

attributes may be satisfactory if the matching produces closely

comparable groups. The small number of subjects (twenty)

makes comparability increasingly difficult. Also there was

apparently no pre-experiment analysis of attributes or a pre-

test to establish baseline data for matching.

2. Experimenter bias effects are probable since

Kipperman was the sole experimenter throughout the research

period. He was aware of all of the treatments presented, to

which subjects each was presented, and recorded all of the

associated data.

3. Subject bias effects are probable since each

individual was aware of what type of treatment was being

administered to them. Tracking task scores were also available

after each trial plus EMG levels if they wished.

4. Though beneficial effects of biofeedback did not

develop in the subjects, the placebo effect in research of

this kind should be controlled. As mentioned in Chapter IV,

the placebo effect is usually strong in any therapy oriented

82

research with human subjects, and biofeedback is primarily an

internal therapy of self-regulation.

5. A problem alluded to in the introduction, the

constant biofeedback signal affecting concentration on the

task, may very well have contributed to a degradation of

performance causing part of the erroneous results. Most of

the experimental literature details the process of biofeed-

back training as a long term effort which is usually dis-

continued when "learned." The technique then became a purely

internal one.

6. External validity problems should be fairly

obvious from the discussion in Chapter III. Reactive arranje-

ment effects are inescapable with the unique equipment involved

and selection and treatment interactions are present by draw-

ing subjects from a very limited sub-population (AFIT students)

to represent the world of pilots.

The conclusions noted above, for the most part, do not

reflect on Kipperman's competence as a researcher per se but

on the actual methodology used. As mentioned early on, in

Chapter II, there are several constraints that Experimenters

must deal with that affect the experiment design approach.

Many of them, including items such as time available, cost

factors, and availability of experimental subjects are factors

that weigh heavily on AFIT student research. On a personal

note, this author has gained much as a result of researchinc

the literature for this thesis--certainly an overwhelminc

83

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awareness for the complexity and difficulty of what is

involved in achieving a valid experiment design has been

driven home. With that thought in mind, the last section

addresses a few provisional recommendations.

Recommendations

This author respectfully suggests the recommendations

below should further attempts be taken to research relation-

ships between biofeedback and task performance. It should

also be realized that these recomendations come not from

many years of experience but solely from gleaning the research

material for this thesis.

1. A thorough training program, to learn how to

voluntarily control a physiological response, should be under-

taken prior to subjects performing a task. Experimental

subjects should be pretested for this control ability without

the necessity for an active biofeedback signal. Researchers

(9:15; 39:150), at least in the clinical arena, point out that

in order for voluntary control of internal responses to be

effective in the "real world" individuals must be able to

elicit this control without requiring constant biofeedback

signals.

2. The double-blind methodology, described in

Chapter IV, along with some form of pretest-posttest placebo

control group design seem to hold the most promise for

satisficing (achieving objectives within reason) experimental

validity. Recognizing the complexity and scope of effort

84

-'. .- i

required to accomplish a design of this type, it is this

author's opinion that it is beyond the capacity of an AFIT

student, given the limited time and resources available.

Perhaps a member of the faculty as the researcher, with AFIT

students as "blind" experimenters, and drawing subjects from

a more stable population would be more suitable.

Probably, other experiment designs could be used with

varying success; some better, some worse. The researcher, in

the final analysis, must weigh all the factors to determine a

"best" design approach and then correctly use statistics as

an aid in "proving" or disproving any hypothesis. The

researcher must protect against faulty designs and hypotheses;

otherwise, all sorts of invalid proofs may materialize. As a

final note, witness this old story related by Hooke (22:94)

. . . about a flea trainer who claimed that fleashear with their legs. As proof, he taught somefleas to jump at his shout of "Jump!" Afteramputating the fleas' legs and observing thatthey no longer responded to his shouts, he restedhis case.

85

SELECTED BIBLIOGRAPHY

86

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NEW_

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26. Kipperman, Captain Mark C., USAF. "Use of Electro-myogram Information to Improve Human OperatorPerformance." Unpublished master's thesis.GSM/SM/79D-18, AFIT/EN, Wright-Patterson AFB OH,December 1979.

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90

BIOGRAPHICAL SKETCH OF THE AUTHOR

Captain Gilbert Fried enlisted in the Air Force in

August 1968 and performed duties in the weather observer

career field. Through the Airman Education and Commissioning

Program he graduated from the University of New Hampshire, in

January 1973, with a Bachelor of Science degree in Mechanical

Engineering. After completing Officer Training School, he

served as a test project manager with the 6511th Parachute

Test Squadron, National Parachute Test Range, El Centro,

California, through March 1977. His next assignment was with

the 6514th Remotely Piloted Vehicle/Cruise Missile Recovery

Test Squadron, Hill AFE, Utah, through May 1979. Following

the Air Force Institute of Technology graduate degree program,

Captain Fried will be assigned to the 6585th Test Group,

Holloman AFB, New Mexico, as a Flight Test Project Officer.

91